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Interpreting Pre-trends as Anticipation: Impact on Estimated TreatmentEffects from Tort Reform

Anup Malani, Julian Reif

PII: S0047-2727(15)00012-2DOI: doi: 10.1016/j.jpubeco.2015.01.001Reference: PUBEC 3542

To appear in: Journal of Public Economics

Received date: 17 June 2013Revised date: 21 January 2015Accepted date: 23 January 2015

Please cite this article as: Malani, Anup, Reif, Julian, Interpreting Pre-trends as An-ticipation: Impact on Estimated Treatment Effects from Tort Reform, Journal of PublicEconomics (2015), doi: 10.1016/j.jpubeco.2015.01.001

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Interpreting Pre-trends as Anticipation: Impact on

Estimated Treatment Effects from Tort Reform

Anup Malani and Julian Reif∗

January 30, 2015

Abstract

While conducting empirical work, researchers sometimes observe changes in

outcomes before adoption of a new policy. The conventional diagnosis is that

treatment is endogenous. This observation is also consistent, however, with an-

ticipation effects that arise naturally out of many theoretical models. This pa-

per illustrates that distinguishing endogeneity from anticipation matters greatly

when estimating treatment effects. It provides a framework for comparing dif-

ferent methods for estimating anticipation effects and proposes a new set of

instrumental variables to address the problem that subjects’ expectations are

unobservable. Finally, this paper examines a specific set of tort reforms that

was not targeted at physicians but was likely anticipated by them. Interpreting

pre-trends as evidence of anticipation increases the estimated effect of these

reforms by a factor of two compared to a model that ignores anticipation.

Keywords: Anticipation, Medical Malpractice, Endogeneity, Tort Reform

JEL Classification Numbers: C50, K13, J20

∗University of Chicago, RFF and NBER; University of Illinois at Urbana-Champaign and IGPA.We thank Dan Black, Amitabh Chandra, Tatyana Deryugina, Steve Levitt, Jens Ludwig, DerekNeal, Seth Seabury, Heidi Williams, participants at workshops and conferences at IGPA, HarvardUniversity, New York University, the Searle Center at Northwestern University, and the Universityof Chicago, and two anonymous referees for helpful comments. Anup Malani thanks the Samuel J.Kersten Faculty Fund at the University of Chicago for funding. Julian Reif thanks the NationalScience Foundation for financial support.

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While conducting empirical work, researchers sometimes observe changes in out-

comes before adoption of a new treatment program or policy. Figure 1 provides an

example from the medical malpractice liability context. It shows that equilibrium

physician labor supply increased well before states adopted caps on punitive dam-

ages, which lower physician liability. The conventional diagnosis researchers make

upon observing such a pattern in the data is that the treatment was endogenous:

states adopted these caps in response to the change in supply or for reasons corre-

lated with supply (Angrist and Pischke 2008, chapter 5).

Figure 1: Excess physician supply before and after punitive damage caps: annual leadsand lags from 5 years before to 5 years after adoption

!0.04

!0.03

!0.02

!0.01

0

0.01

0.02

0.03

0.04

!6 !4 !2 0 2 4 6

Excess!supply!of!Ln(doctors/population)!

Year!relative!to!adoption

Point"estimate 95%"Confidence"interval

This figure plots the normalized coefficients λj from the following regression: yist = Σ5j=−5

λjDst+j +γis+γit+uist,

where yist is the log of the physician count for specialty i in state s in year t, Dst+j is an indicator for whether

punitive damage caps is adopted in period t+ j, and γis and γit are state-specialty and specialty-year fixed effects.

Observing changes in outcomes prior to treatment is also consistent, however, with

anticipation effects. Perhaps individuals began changing their behavior in response to

an expectation that they would be treated in the future. Anticipation is a reasonable

diagnosis if individuals are forward looking, have access to information on future

treatment, and there is a benefit to acting before treatment is adopted.1

1This paper is motivated by a case where there are differential pre-trends, i.e., different pre-trends in units that are treated and in units that are not. However, it is possible for anticipationto exist even when there are parallel pre-trends, i.e., identical pre-trends in both types of units.Suppose there are two states in which doctors have similar expectations about whether a cap will be

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It is very difficult to rule out endogeneity as an explanation for the pre-trends

such as those in Figure 1, although previous studies have argued that the adoption

of punitive damage caps was an exogenous event in the medical malpractice context

(Avraham 2007, Currie and MacLeod 2008).2 It may be equally difficult, however,

to rule out anticipation as an explanation for pre-trends. For example, we present

evidence that these reforms were discussed in newspapers years prior to their adoption

and that there are economic reasons for doctors to change behavior prior to reforms.

Our point is not that the pre-trends in Figure 1 must be anticipation rather than

endogeneity. Rather, we argue that there is no good reason to estimate the treatment

effect of punitive damage caps on physician supply assuming that pre-trends can only

be evidence of endogeneity. They could also be due to anticipation. This matters

because how one interprets these pre-trends has substantial implications for how

one estimates treatment effects and how large those estimates are. For example, a

researcher who does not account for anticipation effects with the same sign as post-

adoption effects of a policy will underestimate the full treatment effect of that policy.

With this objective in mind, we organize the paper around two contributions. Our

first contribution is to provide a framework for rigorously comparing and estimating

the different models that may be employed to estimate anticipation effects. We start

from the premise that there exists a wide array of applied economics topics in which a

researcher may be confronted with forward-looking agents whose responses anticipate

future treatment. Economic theory suggests, for example, that individuals are forward

looking when purchasing durable goods such as cars or houses or making human

capital investments, and that firms are forward looking when investing in physical

capital or entering new markets.3

Two main difficulties arise when estimating models with anticipation effects. One

is that researchers may not know how many periods in advance agents anticipate

treatment. A common response in the empirical microeconomics literature is to esti-

adopted at some future date t, but at date t only one of the states actually adopts a cap. Pre-trendswill be parallel and only post-treatment outcomes will diverge, yet there are anticipation effects byassumption.

2Although we selected our application because treatment is likely to be exogenous, it is possiblethat treatment is anticipated even when it is endogenous. Our methods may be useful even in thatcontext, though care is required in interpreting results. For example, if it is known that endogeneityand anticipation work in opposite directions, our methods yield a bound.

3Specific examples include R&D investment decisions (Acemoglu and Linn 2004), present valueasset pricing models (Chow 1989), pricing of durable goods (Kahn 1986), real estate pricing (Poterba1984), and investment in human capital (Ryoo and Rosen 2004).

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mate a “quasi-myopic”model that includes anticipation terms for only a finite number

of periods.4 Within these periods, however, anticipation effects are estimated in a

non-parametric manner.

An alternative approach, common in the finance and macroeconomics literature,

is to posit outcomes as a function of exponentially discounted expectations about

future treatment (e.g., Chow 1989). In this formulation treatment typically has a

constant contemporaneous effect and an exponentially discounted anticipation effect.

Exponential discounting has the useful feature that suitable differencing can eliminate

nearly all anticipation terms.

We do not endorse any particular parameterization. The optimal approach will

depend on the theory motivating the empirical analysis and on the limitations of

the data. Instead, our framework advances the literature by highlighting the precise

assumptions required to generate the regression models estimated in prior literature.

It also provides a common benchmark for both the quasi-myopic and exponential

discounting models that for the first time allows a comparison of the merits of each.

Another difficulty with estimating a model of anticipation effects is that expecta-

tions are generally unobserved. A common response is to examine shocks that alter

expectations about treatment but do not actually administer a treatment. An exam-

ple is a regulation that is enacted at time t but not implemented until time t+k (e.g.,

Alpert 2010, Blundell, Francesconi, and Van der Klaauw 2010, Gruber and Koszegi

2001, Lueck and Michael 2003). Unless actual expectations are observed, however,

the investigator can merely demonstrate that expectations affect outcomes. She can

not identify the precise slope of the relationship and thus can not identify treatment

effects that incorporate full anticipation effects.5

An alternative approach is to assume a model of belief formation, such as rational

4A less than comprehensive list includes: Acemoglu and Linn (2004), Autor, Donohue, andSchwab (2006), Ayers, Cloyd, and Robinson (2005), Bhattacharya and Vogt (2003), Finkelstein(2004), Gruber and Koszegi (2001), Lueck and Michael (2003), and Mertens and Ravn (2011).

5There is also a separate literature on Ashenfelter dips, in which an observed pretrend goes in theopposite direction as the post-implementation effects of treatment (Ashenfelter 1978). The usualinterpretation of such a dip is endogenous selection. A typical solution is to net out the dip bycomparing post-implementation outcomes to pre-dip outcomes, in which case the slope of the dipdoes not matter. However, it is also possible for anticipation to cause opposite-signed pre-trends,in which case netting them out is inappropriate. For example, Lueck and Michael (2003) discuss acase where landowners were found to have killed endangered species on their land in anticipation ofa law prohibiting development in areas inhabited by these species. This anticipation effect has theopposite sign of the post-implementation effect of the law, which preserves endangered species.

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or adaptive expectations, in order to substitute observable variables for unobservable

expectations of a variable. Unless the forecast error is orthogonal to the observable

variables, however, the researcher will have to instrument for them. The traditional

source for these instruments is a subset of the agent’s information set, for instance,

lags of the observable variable (McCallum 1976). These lags influence the agent’s

unobservable forecast of a variable but do not directly influence the outcome variable.

A key technical innovation in this paper is our proposal of a novel, alternative set

of instruments: leads of the observable outcome or treatment variable. In general,

leads can complement lags as instruments for expectations in the forward-looking

regression. We show there are situations in which lags or leads are invalid, though

leads are somewhat more robust.

Our second contribution is that we explore the practical implications of the fore-

going analysis in an empirical application. Specifically, we estimate the effect of

punitive damage caps on equilibrium physician supply and show that accounting for

anticipation could increase their estimated effect by a factor of two or more compared

to a model that ignores anticipation. We first estimate a model that ignores anticipa-

tion and thus corresponds to prior analyses of tort reform, e.g., Klick and Stratmann

(2007). We find that caps on punitive damages have a positive treatment effect on

physician supply of 1.1 percent after implementation of caps. Then, we interpret the

pre-period trends visible in Figure 1 as evidence of anticipation effects and estimate

the different regression models discussed in our framework. We find that damage

caps have a 1.5 to 2.6 percent post-implementation effect after accounting for all

prior anticipation effects. In addition, we estimate that damage caps had a 0.9 to 1.9

percent effect in each of the two years immediately preceding reform. By contrast,

prior models implicitly assume zero treatment effects prior to reform. Our results are

robust to different models of anticipation, which suggests that the choice of how to

parameterize anticipation effects is not critical to our estimates of those effects for

our particular application.

The following is an outline of the remainder of the paper. Section 1 reviews

the parameters of interest in a forward-looking regression. Section 2 elaborates on

the various parametric restrictions that may be employed to reduce the number of

expectation terms in the forward-looking regression. Section 3 discusses how to es-

timate the forward-looking regression model for a given model of belief formation.

It introduces a new set of instruments, leads of the outcome variable, that can be

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employed to address endogeneity from forecast errors. Section 4 applies the different

approaches to estimating the forward-looking model using data on tort reform and

physician supply. Section 5 concludes with suggestions for future research.

1 Parameters of interest

Our anticipation effects framework begins with a forward-looking regression of the

form

yt = λ0dt + Σ∞

j=1λjEt [dt+j] + et (1)

where yt is some outcome, {dt+j} are a sequence of future values or discrete treatment

states, Et indicates expectation taken with respect to an agent’s information set at

time t, and et is an idiosyncratic error term uncorrelated with the regressors. This

specification has been used, often with further parametric restrictions, in a wide array

of theoretical models (e.g., Acemoglu and Linn 2004, Becker, Grossman, and Murphy

1994, Chow 1989, Kahn 1986, Poterba 1984, and Ryoo and Rosen 2004).

Before estimating this regression, it is useful to define the possible parameters

of interest from a policy evaluation standpoint. For simplicity, consider the case

where a binary treatment is implemented permanently in time t∗, and assume that

individuals have perfect foresight. The baseline is outcomes at time t∗ − ∞, before

agents anticipated adoption of treatment.

The first parameter of interest is the average per-period effect of treatment on

outcomes after implementation: λ0 + Σ∞

j=1λj.6 We call this the ex post effect of

treatment. This parameter can itself be broken down into two components. One is

the ex post non-anticipation effect of treatment, or λ0. This is the effect on outcome

yt of a treatment at time t that is expected to last only one period. The other

component is the ex post anticipation effect, or Σ∞

j=1λj. One can interpret this as the

effect on yt of the agent’s expectations about whether treatment will continue to be in

effect in future periods. A treatment that is implemented permanently will have the

same ex post non-anticipation effect as a treatment that is only implemented for one

period, but the latter will have a smaller ex post anticipation effect if agents correctly

anticipate that it is temporary.

6If individuals lack perfect foresight, the estimated effect will differ as each λj , j > 0 will haveto be weighted by E [dt+j ] < dt+j . A similar issue will arise for the ex ante effect.

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Figure 2: Parameters of interest

Permanent treatment adopted at time !"

Time

#

!

Ex post effect

Ex ante effect

at time !" $ %

!"!" $ %

A second parameter of interest is the ex ante effect in period t∗ − k for k > 0:

Σ∞

j=kλj. This captures the average effect on pre-implementation outcome yt−k of a

permanent treatment implemented at time t∗ and is driven entirely by anticipation

effects. This parameter changes over time because of discounting and because agents

might update their expectations when they receive new information.

Figure 2 illustrates the effect of a permanent treatment implemented in period

t∗, but anticipated in all prior periods. To simplify the graphical expression, we

assume time is continuous rather than discrete. The height of the curve prior to

time t∗ corresponds to the ex ante effect, and the height of the curve after time t∗

corresponds to the ex post effect. The full effect of treatment on outcomes is the

area under the solid line. It depends on both the ex ante and ex post effects.

We emphasize that observing data as in Figure 2 is not proof of anticipation. It

could be evidence of endogeneity, or both anticipation and endogeneity. We do not

provide a test that sharply discriminates between the two explanations. However, if

agents do anticipate treatment and the investigator does not account for this during

estimation, there are two reasons to think that her estimate of the full effect of

treatment will be biased.

First, the investigator is likely to ignore the ex ante effect, which occurs prior to

adoption of treatment. Standard econometric models implicitly assume this effect is

equal to zero. But if outcomes change prior to treatment and this change is caused

by anticipation of treatment, it should be counted towards the full treatment effect.

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Second, ignoring the ex ante effect will cause the investigator to estimate with bias

the ex post treatment effect. We elaborate on this second point in the next section.

The sign of the bias from ignoring anticipation effects in econometric modeling

depends on whether the sign of anticipation effects is the same as that of non-

anticipation effects and whether there is endogeneity. If the signs are the same and

there is no endogeneity, the investigator will likely underestimate the absolute value

of the full treatment effect. First, she will ignore the ex ante effect, which has the

same sign – a conceptual error. Second, her empirical model, likely the myopic model

we describe in the next section, will not fully capture ex post anticipation effects – an

econometric error. If the signs of anticipation effects and non-anticipation effects are

different or if there is endogeneity, one cannot in general sign the bias from ignoring

anticipation effects.

If there are no anticipation effects but the investigator’s econometric models mis-

takenly assume anticipation is present, the nature of bias in the resulting estimates

will depend on the presence of endogeneity. If there is no endogeneity, the anticipation

models we describe in the next sections will inefficiently include extraneous regressors,

but estimates will remain unbiased. If there is endogeneity, bias may ensue, and it

cannot in general be signed without making further assumptions. This underscores

the need for the investigator to make cogent arguments in favor of exogeneity.

2 Simplifying the forward-looking model

The primary challenges with estimating a forward-looking model such as (1) are the

potentially infinite number of expectation terms (“dimensionality” problem) and the

lack of data on expectations (“unobservable expectations” problem). A researcher

with a finite data set must choose some parametric restriction on the model because

(1) cannot be estimated due to the dimensionality problem.

Here we discuss three different ways to tackle these two problems. First, a re-

searcher might completely ignore anticipation effects. Second, a researcher might es-

timate a quasi-myopic model that includes only a finite number of anticipation terms.

Third, a researcher could adopt an exponential discounting model that assumes out-

comes are a function of exponentially discounted expectations about treatment.

We do not endorse any particular approach, though the first approach is surely

the least satisfactory due to omitted variable bias. Towards the end of this section we

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discuss the relative merits of the quasi-myopic and exponential discounting models

and emphasize that these two approaches are complementary.

2.1 Addressing the dimensionality problem

Myopic model. The simplest approach to dealing with anticipation effects is for

the econometrician to ignore them and estimate a myopic model such as

yt = βmyopic0 dt + ut (2)

where yt is the outcome of interest, dt is the treatment, and ut includes the model

error, et, from the forward-looking model (1) and also additional error resulting from

model misspecification. This is the model researchers typically use when they assume

no anticipation effects.

The omission of anticipation effects generates omitted variable bias. The specific

nature of the bias depends on which parameter of interest one seeks to estimate. We

will focus on the ex post effect of treatment because it corresponds closely to what

most applied researchers are interested in estimating when working in an environment

with no anticipation. If the true specification is the forward-looking model (1), then

the treatment effect estimated by the myopic model is equal to

plim |β̂myopic0 | = |λ0|+ Σ∞

j=1 |λj|αj

where αj is the coefficient from a regression of expected future treatment, Et [dt+j], on

current treatment, dt.7 Intuitively, the coefficient on current treatment in the myopic

model captures some of the effect of future treatment. It differs from the ex post

effect, λ0 + Σ∞

j=1λj, by the coefficients αj.

The coefficient αj will usually be positive because current treatment and expec-

tations of future treatment are likely to be positively correlated.8 Moreover, the

magnitude of αj will be less than one unless the current state of treatment perfectly

7The econometrician has the same problem estimating the αj coefficients as she does estimatingthe coefficients in the quasi-myopic model we describe in the next section: she does not observeexpected future treatment terms.

8Negative correlation between current treatment and expected future treatment implies thatsubjects frequently alternate between treated and untreated states. It is difficult to come up withexamples of such treatments. Zero correlation is possible, but rules out infrequent treatment ortreatment that lasts multiple periods.

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Figure 3: Estimate from a myopic model

!"#$%&'()

*+ , -

.'&/0 1 234#5 63

Time

.

*+

.'78/9$':8

1234;< 6<

-

.'78

Permanent treatment adopted at time *+

234#5 63 (Ex post effect)

predicts all future expected states of treatment. Thus, assuming λ0 and {λj} have

the same sign, the myopic model is likely to underestimate the magnitude of the ex

post effect.

This point is illustrated in Figure 3, which plots the outcome of a forward-looking

process after adoption of a permanent treatment at time t∗. The true ex post ef-

fect of the intervention is to increase outcomes by Σ∞

j=0λj = ypost − ypre per period.

Estimation of a myopic model, however, yields a treatment effect, β̂myopic0 , that is

the difference between the average outcome, ysamplepre , before the law is passed and the

average outcome, ypost, after the law is passed. The myopic estimate is less than the

true ex post effect because the researcher observes a finite number of pre-treatment

periods, say [t∗ − k, t∗], but expectations may have begun shifting outcomes well be-

fore t∗. Therefore the average pre-treatment outcome in the sample, ysamplepre , is greater

than the true pre-treatment outcome, ypre.

Quasi-myopic model. To address the shortcomings of the myopic model, a

researcher might estimate a quasi-myopic model that assumes agents have anticipation

effects, but only for a finite number of periods S:

yt = βquasi0 dt + ΣS

j=1βquasij Et[dt+j] + ut (3)

This addresses the dimensionality problem by ignoring anticipation terms after S

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periods, perhaps on the theory that agents do not forecast further than S periods

ahead or that anticipation effects past S years have negligible effects.

Exponential discounting model. The third approach to reducing the dimen-

sionality of the forward-looking model is to assume that treatment has a constant

contemporaneous effect of λ0 = β and an anticipation effect j periods prior to treat-

ment of λj = βθj:

yt = βdt + βΣ∞

j=1θjEt [dt+j] + ut (4)

The ex post effect of treatment is then estimated as β̂/(1 − θ̂). The central benefit

of the assumption that outcomes are a function of exponentially discounted expecta-

tions about treatment is that subtracting θyt+1 from (4) will enable the researcher to

generate an equation with only two regressors.

2.2 Addressing the unobservable expectations problem

Both the quasi-myopic and exponential discounting model contain unobserved expec-

tations as regressors. A common solution to addressing the unobservable expectations

problem is to assume a model of belief formation, such as rational or adaptive expec-

tations, in order to substitute observable variables for unobservable expectations of a

variable. Below we derive a solution under the assumption that agents have rational

expectations. We model adaptive expectations in Appendix A. We confine our dis-

cussion to the exponential discounting model because estimates of the quasi-myopic

model typically substitute realizations, dt+j, for expectations, Et[dt+j], rather than

modeling expectations directly. However, it is possible to generalize our modeling of

beliefs for the exponential discounting model to the quasi-myopic model.

In general, expectations may depend on realizations (E [z] = z + v) or vice versa

(z = E [z] + v). Economic theory should dictate which path to take. We focus here

on the case where expectations depend on realizations because this corresponds to

the application we consider in Section 4. We consider alternative formulations of the

rational expectations assumption in Appendix B.

Let expectations be a function of treatment so that Et [dt+j] = dt+j + vt,t+j, where

E[dt+jvt,t+j] = 0 and vt,t+j is the forecast error resulting from an agent’s time-t

forecast of the treatment dt+j. In this case we can substitute the rational expectations

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assumption directly into the exponential discounting model to obtain

yt = βΣ∞

j=0θjdt+j + et + βΣ∞

j=1θjvt,t+j

Subtracting θyt+1 from yt then yields

yt = θyt+1 + βdt + wt (5)

where

wt = et − θet+1 + βΣ∞

j=1θjvt,t+j − βΣ∞

j=2θjvt+1,t+j

= [et − θet+1] + βθvt,t+1 + βΣ∞

j=2θj[vt,t+j − vt+1,t+j]

The error term wt has three components. One is the change in model error,

et − θet+1. A second is the error in forecasting time-t + 1 treatment at time t. The

third component is the change in forecasts about time t + j treatment (j > 1) from

time t to time t + 1. There is, however, only one definite source of endogeneity

between outcome yt+1 and the error term: the model error et+1.9 Section 3 of our

paper discusses how to employ instruments to overcome this problem.

2.3 Comparing models of anticipation

We do not endorse the quasi-myopic model over the exponential discounting model

or vice versa. Each model has imperfections and the choice between the two should

be dictated by the theory motivating the empirical analysis and the available data.

The quasi-myopic model has two shortcomings. First, it assumes that there are no

more than S periods of anticipation effects. If this assumption is incorrect then, as in

the myopic model, bias ensues. Moreover, if the length T of the panel of data available

to the researcher is less than S, the researcher cannot estimate all anticipation effects.

Second, the way that the quasi-myopic model is actually implemented in the liter-

ature implicitly substitutes realizations, dt+j, for expectations, Et[dt+j], of treatment

9There is no endogeneity from vt,t+1 because, although yt+1 is a function of dt+1, we haveassumed that dt+1 is orthogonal to vt,t+1. Nor is there endogeneity from the change in forecasts(vt,t+j − vt+1,t+j , j > 1) because under rational expectations these forecast updates are orthogonalto prior forecast errors (vt,t+j) and thus orthogonal to Et [dt+j ] too. Indeed, there is no additionalendogeneity even if {dt} are serially correlated because E[dt+jvt,t+j ] = 0 by assumption.

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in (3). This introduces measurement error bias unless agents have perfect foresight.

One solution to the measurement error problem is to instrument for the affected re-

gressors, using analogous methods to those we employ for the exponential discounting

model. However, this requires at least S instruments for the S periods of anticipation

effects the researcher seeks to estimate. The exponential discounting model, however,

only requires one instrument.

A problem with the exponential discounting model is that it assumes expectations

decay at an exponential rate, which is an admittedly strong assumption, perhaps

motivated by convenience of estimation rather than theory. That said, there are

numerous theoretical models with exponential discounting of future income or utility

that yield regression models with exponential discounting of expected treatment.

Even as an ad hoc assumption on a regression model, exponential discounting does

not appear any more troubling than the possibly incorrect but frequent assumption

in theoretical models that future profits or utility are exponentially discounted.

A second issue with the exponential discounting model is that modeling expecta-

tions generally requires imposing structure on the error term. We discuss this in more

detail in Section 3. Of course, if one is to take unobserved expectations seriously in

the quasi-myopic model, one may have to impose structure on the error term in that

model as well.

We emphasize that one cannot, a priori, determine whether the parametric restric-

tions in the quasi-myopic model or those embodied in the exponentially discounted

model yield lower bias. If there are more than S periods of anticipation effects, then

the quasi-myopic model suffers omitted variable bias. But exponential discounting

may also be a poor approximation to the time path of anticipation effects and suffer

misspecification bias.

These competing arguments aside, we note that these regression models are not

mutually exclusive. For example, one could specify an estimating equation with a few

quasi-myopic terms in addition to an exponentially discounted expectations process.

Although this layering increases data and power requirements, it does permit one to

check if the quasi-myopic model is empirically more appropriate by testing whether

the included quasi-myopic terms are statistically significant.

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3 Estimation

This section takes up estimation of anticipation effects models. The focus will be

on estimating the exponential discounting model, though the section will contain

lessons for the quasi-myopic model as well. The Euler equation (5) derived in the

previous section greatly reduced the dimensionality of the forward-looking model (1),

but consistent estimation still requires, at a minimum, that the researcher address

the correlation between yt+1 and the model error et+1 contained in the error term wt.

One solution is to find an instrument.

The usual source for these instruments is a subset of the agent’s information set,

for instance, lags of the endogenous variable (McCallum 1976). This is typically

motivated by modeling expectations as a linear projection of the variables in the

agents’ data sets, which include lagged values of the endogenous variable. An alter-

native motivation is to note that since yt+1 and its lags all depend, according to the

forward-looking model (1), on expectations about future treatment, changes in those

future expectations will move both lags of yt+1 and yt+1. The exclusion restriction is

completed by noting that yt in equation (1) does not depend on lagged values.

This alternative motivation suggests a new set of instruments we propose here:

leads of the endogenous variable. Like yt+1, {yt+k} for k > 1 depend on expectations

about future treatment and thus are correlated with Et [yt+1]. Leads meet the exclu-

sion restriction because, as shown by equation (5), the current outcome yt is related

to future treatments, and thus future outcome variables, only through yt+1.

One could alternatively instrument for yt+1 using leads of dt+1 rather than leads

of yt+1 since shocks to future expectations of dt+1 are what ultimately drive iden-

tification. Whether this is more efficient than using leads of yt+1 depends on the

variance-covariance structure of model error et and forecast error vt, which is un-

known a priori. However, there is a strong practical reason to prefer leads of yt+1:

they embed more information than leads of dt+1 for any finite data set. For example,

consider a panel with 10 time periods. Instrumenting for y9 with y10 necessarily in-

cludes information about {d11, d12...} because y10 is a function of future treatments.

That information is unavailable when using leads of d9, however, because the data set

only contains 10 time periods. This advantage is reduced if data on the future treat-

ments {d11, d12, ...}, but not the future outcomes {y11, y12, ...}, are available. There

are some scenarios, however, where using leads of dt is preferable to using leads of

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yt+1. We discuss them at the end of this section.

Below, we derive the technical conditions necessary for estimation to be consistent.

We work with a model that generalizes equation (5) to a panel setting and allows us

to draw on results from the literature on dynamic panel estimation. The main result

is that estimation requires imposing some degree of limited serial correlation. One

might think this is a poor assumption in a panel data setting (Bertrand et al. 2004).

However, if errors are uncorrelated across panels then it is possible to test for serial

correlation (Arellano and Bond 1991). Moreover, we emphasize that this issue is not

unique to the exponential discounting model. Estimating the quasi-myopic model

requires the researcher either to instrument for that model’s future expectations,

which bring up analogous problems, or to assume perfect foresight, which is difficult

to justify (Gruber and Koszegi 2001).

3.1 Instrumenting with lags and leads

We are interested in estimating a model of the form

yit = θyi,t+1 + α1xit + α2xi,t+1 + βdit + ηi + wit (6)

where i = 1...N, t = 1...T , and 0 < θ < 1. We assume that ηi and wit are inde-

pendently distributed across i with E [ηi] = E [wit] = E [ηiwit] = 0. The number of

time periods T is fixed and the number of individuals N is large. Without loss of

generality, we assume that xit and xi,t+1 are strictly exogenous and known in advance.

Although we shall focus here on the validity of instrumenting with leads, it is easy to

adapt our argument to show that lags are also valid.

Direct OLS estimation of equation (6) is inconsistent because E [yi,t+1ηi] 6= 0. Esti-

mating first differences (defined here as ∆yit = yit−yi,t+1) fails because E [∆yi,t+1∆wit]

6= 0. A within estimator suffers from this same problem, although the bias may dis-

appear as T −→ ∞. The logic in Arellano and Bond (1991), Arellano and Bover

(1995), and Blundell and Bond (1998) suggests that one solution is to instrument for

∆yi,t+1 using leads of yi,t+1. Leads are valid instruments if the following standard

assumptions are met:

A1: E [yiTwit] = 0 ∀ i, ∀ t ≤ T − 1

A2: E [wiswit] = 0 ∀ t 6= s

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A3: E [ηi∆wi2] = 0 ∀ i

Assumption A1 requires yiT to be uncorrelated with past disturbances. Assump-

tion A2 requires these disturbances to be uncorrelated. These two assumptions to-

gether imply the following moment conditions:

E [yi,t+j∆wit] = 0 ∀ j ≥ 2, ∀ t (7)

Assumption A3 requires the terminal conditions to be mean stationary. In other

words, conditional on the covariates xit, individuals with large random effects ηi must

not be systematically closer or farther away from their steady states than individuals

with small random effects, so that the terminal conditions are representative of the

steady state behavior of the model. If it holds, A3 implies the following additional

moment conditions:

E [∆yi,t+1wit] = 0 ∀ t (8)

The model is overidentified if T > 3 but can be estimated using the Generalized

Method of Moments (GMM) framework developed by Hansen (1982). “Difference

GMM”estimation exploits the moment conditions (7) while “system GMM”estimation

exploits both (7) and (8).

Assumption A2 is central to the validity of these estimation procedures. As cur-

rently stated, however, it is actually stronger than necessary. Limited serial corre-

lation of order H > 0 is acceptable so long as the researcher takes care to omit the

affected instruments and enough instruments remain for identification. We therefore

loosen A2:

A2′: E [witwit+j] = 0 ∀ j > H, H ≥ 0

This changes our moment conditions (7) and (8) to

E [yi,t+j∆wit] = 0 ∀ j ≥ H + 2, ∀ t

E [∆yi,t+H+1wit] = 0 ∀ t

Whether or not these assumptions are satisfied depends on the content of the er-

ror term in the Euler equation (5), which in turn depends on how expectations are

specified.

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For notational convenience, we now drop the i subscript for the remainder of this

section. Following Section 2.2, we consider the case where expectations are a function

of treatment: Et [dt+j] = dt+j + vt,t+j. The error term, derived in equation (5), is

wt = et − θet+1 + βθvt,t+1 + β(Σ∞

j=2θj[vt,t+j − vt+1,t+j])

In order for the error term wt to satisfy Assumption A2’, the following four conditions

must be satisfied for all periods and all agents, for some H ≥ 1:

1. E [etet+j] = 0 ∀ j > H

2. E[etvt+j,t+k] = 0, ∀ k > j, ∀ j > H

3. E[(vt,t+k − vt+1,t+k)vt+j,t+j+1] = 0 ∀ k > 1, ∀ j > H

4. E[(vt,t+k − vt+1,t+k)(vt+j,t+m − vt+j+1,t+m)] = 0 ∀ k > 1, m > j + 1, j > H

In words, condition 1 means autocorrelation in model error et cannot be higher

than order H. Condition 2 means the model error is orthogonal to the H-step-ahead-

and-beyond forecast error. Condition 3 means the change in a forecast from period t

to period t+ 1 is uncorrelated with the level of a forecast in period t+ j. Condition

4 means independent information is used to update the forecast each period.

Conditions 1, 2 and 4 are plausible in many scenarios, but condition 3 may be

an unrealistic assumption. It holds in the cases of perfect serial correlation (so

the change in forecast (vt,t+k − vt+1,t+k) is equal to 0) or no serial correlation (so

E[vt+j,t+j+1vt+l,t+k] = 0 ∀ j, k, l). These two extremes are not satisfied in most ap-

plications. Rational expectations, however, offers some hope. It implies that the

(perhaps nonzero) expectation in Condition 3 is not a function of t. In other words,

an agent’s forecast error might depend on whether she is predicting an event three

time periods in the future versus four time periods in the future, but it does not

depend on the particular time period she is forecasting from.

This means we can rewrite our moment conditions (7) and (8) as

E [yt+j∆et − k1 (j; β, θ)] = 0

E [∆yt+jet − k2 (j; β, θ)] = 0

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where k1 (·) and k2 (·) are constants that do not depend on t or the data. They will

be absorbed into the constant term, which means the researcher can still identify

the parameters of interest, β and θ.10 Unfortunately, the non-zero moment condition

differs for each instrument, which means the researcher may not be able to simultane-

ously include multiple instruments from different time periods. The optimal solution

is for the researcher to specify each instrument as a separate GMM equation and then

estimate the entire system simultaneously.

Finally, we note that estimation is further complicated when the treatment vari-

able is discrete. We discuss how to handle the binary case in Appendix C.

3.2 Comparing lag and lead instruments

The discussion above showed that lags and leads of the outcome variable are both

valid instruments under our standard forward-looking specification when agents have

rational expectations. We also noted that the researcher could alternatively use leads

(but not lags) of the treatment variable as instruments. Here we show that the

possibility of instrumenting with leads of the treatment variable provides a flexibility

that makes leads generally better instruments than lags. We demonstrate this by

considering two common situations that depart from the standard specification.

Suppose, for example, that agents do not continuously update their forecasts of

future variables with new, orthogonal information. In this case lags of the outcome

variable are no longer valid instruments. To illustrate why, we examine the case

where agents have rational (i.e., unbiased) forecasts of treatment but never update

these forecasts (e.g., Anderson, Kellogg, and Sallee 2013; Carroll 2003). This implies

the forecast error no longer depends on the date the forecast was made, so that

Et [dt+j] = dt+j + vt,t+j = dt+j + vt+j. The exponential discounting model may now

be written as

yt = βΣ∞

j=0θj(dt+j + vt+j) + et

10It may appear surprising that we can effectively ignore k1 (·) and k2 (·) even though they arefunctions of our parameters. We are able to do this because k1 (·) and k2 (·) are constants and thusmerely represent level shifts of the GMM minimization problem. Consider the analogous problemfor OLS: min

β0,β1

(y − β1x1 − β0 − k (β1))2where k (β1) is some constant that is a function of β1 and

independent of x1. Identification of β0 is impossible but OLS can still identify β1 even withoutknowing the functional form of k (β1).

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Subtracting yt+1 yields the Euler equation

yt = θyt+1 + βdt + βθvt+1 + et − θet+1

Lags are necessarily invalid instruments in this specification because yt−j for any j > 1

is correlated with vt+1. Leads, however, remain valid instruments.

Alternatively, suppose the researcher derives an Euler condition that includes

lagged dependent variables, e.g.,

yt = θyt+1 + γyt−1 + βdt + wt

In this scenario, leads of yt+1 are invalid instruments for yt+1. The reason is that yt+j

for any j > 1 is correlated with yt and thus wt due to the autoregressive specification

for yt. Leads of the outcome variable are thus no longer orthogonal to the error

term. Lags, however, remain valid instruments. Interestingly, leads of the treatment

variable, dt, are also valid instruments, so long as treatment remains exogenous to

the error term.

4 Application

In this section we estimate the effect of punitive damage caps on physician supply us-

ing the different methods of estimating anticipation effects we have described. Section

4.1 describes the data we employ. Sections 4.2 and 4.3 provide background on medi-

cal malpractice liability and present evidence that changes in the supply of physician

prior to adoption of tort reform are plausibly due to anticipation. Finally, Section 4.4

explains our empirical strategy and Section 4.5 reports our estimates.

4.1 Data

Our analysis employs annual physician count data from the American Medical Asso-

ciation’s Physician Masterfile. These data include private practitioners, hospital staff,

residents, and locum tenens (temporary employees). They exclude military doctors.

Physicians are categorized into one of 20 possible specialties and have state identifiers.

The data span the period 1980-2001, with gaps in 1984 and 1990.

Klick and Stratmann (2007) note that some physician specialties are sued more

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often than others and correspondingly group them into four equally-sized risk tiers,

displayed in Table 1. We use their definitions to limit our data and analysis to the

two riskiest tiers (tiers 1 and 2) because we expect these to be more affected by tort

reform than the other two tiers.

Figure 4 graphs the total counts over time of the five most populated specialties

in the data. The supply of general practitioners is declining over time, the supply of

general surgeons is stagnant, and the rest are rising.

Figure 4: Physician supply from 1980 to 2001

0

10,000

20,000

30,000

40,000

1980 1985 1990 1995 2000

Physician!count

Year

Anesthesiology

General!practice

General!surgery

Obstetrics!and!gynecology

Orthopedic!surgery

Note: data for 1984 and 1990 are interpolated.

Our tort reform data come from Avraham (2010). These data indicate, for the

same time period as our physician supply data, whether ten different tort reforms are

in effect at the state-year level. These reforms are defined in Table 2 and are coded

as 0-1 indicator variables.

The supporting analysis described in Section 4.3 employs state-level data on per

capita income and medical transfer payments from the Regional Economic Infor-

mation System (REIS). Medical transfer payments include Medicare and Medicaid

payments received by state governments.

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4.2 Background on tort liability and tort reform

Tort liability is akin to a legally-mandated alteration of the implicit labor contract

between a patient and her physician. In most cases, it requires the physician to pro-

vide the quality of care that a “reasonable physician”would provide and compensates

patients who suffer injuries due to inadequate care. Compensation may include eco-

nomic damages for lost wages and the cost of additional medical care; non-economic

damages for pain and suffering from the injury; and punitive damages intended to

punish the doctor for outrageous misconduct.

Policymakers are concerned that tort liability is driving away doctors and thus

reducing patients’ access to care. This claim has received substantial attention from

scholars and the media.11 However, the effect of tort liability on equilibrium physician

supply is theoretically ambiguous. On the one hand, an increase in liability can

increase the cost of providing service and drive physicians away. On the other hand,

if transaction costs prevent a patient and physician from writing a complete contract

that covers all contingencies, including instances of malpractice, then the mandatory

terms imposed by tort liability that improve the contract will increase the value of

(and demand for) physician care.

Tort reform refers to various changes to these mandatory contract terms. Table

2 provides a description of the most common reforms. Most of them, such as caps

on punitive damages, lower damages paid by doctors found liable. Some, like split

recovery, reduce the damages received by patients, and thus their incentive to sue.

Others, such as reform of joint and several liability, reduce the extent to which hospi-

tals share liability and thus effectively increase the overall liability of doctors (Currie

and MacLeod 2008).

Several recent studies analyze the impact of tort liability on physician supply.

Kessler, Sage, and Becker (2005) perform a state-level difference-in-differences analy-

sis and find evidence that reforms directly affecting how much a liable defendant has

to pay increase physician supply by 3%. Matsa (2007) examines the effect of damage

caps on physician supply and finds it increases the supply of physicians by about 10%,

but only in rural counties. Klick and Stratmann (2007) employ a triple-differences

model and estimate that caps on non-economic damages are associated with a 6%

11See Born, Viscusi, and Baker (2006), Currie and MacLeod (2008), Helland, Klick, and Tabarrok(2005), Holtz-Eakin (2004), Kessler, Sage, and Becker (2005), Klick and Stratmann (2007), Matsa(2007), and The Economist (2005).

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increase in physician supply for high-risk specialties relative to low-risk specialties.

In this paper, we focus on the effect of punitive damage caps on physician supply.

We chose this reform for two reasons. First, Figure 1 shows that this reform exhibits

pretrends that are strikingly similar to Figure 2, a canonical illustration of anticipa-

tion effects. This suggests it is a good candidate to illustrate how to estimate our

forward-looking model. Second, prior empirical studies have argued that this reform

was adopted for reasons unrelated to physician supply (Avraham 2007, Currie and

MacLeod 2008).12 We elaborate on this second point in the next section.

4.3 Evidence on anticipation of punitive damage reforms

The existence of pre-trends does not prove that anticipation exists. Indeed, the

conventional diagnosis is that pre-trends imply endogeneity. In this section we cast

doubt on that diagnosis and argue that anticipation is a plausible cause. Historical

accounts of tort reform suggest that punitive damage caps were not driven by events

in the health care industry. Moreover, the data on physician supply contradict the

usual story given for why adoption of punitive damage caps might be endogenous.

Historically, physician lobbies have not focused on enacting punitive damage caps.

Hubbard (2006) notes that physician lobbies focused instead on noneconomic dam-

age caps, period payment, contingency fees, and collateral source. The effects of

these differential lobbying efforts are visible in Table 3, which shows when different

tort reforms were adopted and whether they apply only to medical malpractice. As

expected, the reforms targeted by the physician lobby (noneconomic damage caps,

period payment, contingency fees, and collateral source) are generally aimed at med-

ical malpractice. By contrast, punitive damage caps, along with joint and several

reform and split recovery, stand out as applying to all industries.13

Indeed, punitive damage caps reforms were spurred by events unrelated to the

health care industry (Avraham 2007; Currie and MacLeod 2008). These reforms were

adopted in two waves, one in the mid-1980s and the second in the mid-1990s, and

were driven by well-publicized anecdotes unrelated to physician suits. For example,

the 1980s reforms were triggered by incidents where an insolvent drunk driver or

12Split recovery and joint and several liability also fit these two criteria. An earlier version ofthis paper also examined these reforms and found similar results to the ones presented for punitivedamage caps.

13Table 3 indicates that there are a few states that did actually target their reforms to medicalmalpractice. We exclude them from our main empirical specification.

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hazardous waste operator’s liabilities were reallocated to a solvent municipal entity

under joint and several liability (Rabin 1988). The 1990s reforms to punitive damages

were driven by the well-publicized case of Liebeck v. McDonald’s Restaurants (1994),

which resulted in an initial award of $2.7 million in punitive damages to a lady who

had spilled hot coffee on herself (Nockleby and Curreri 2005).

Looking beyond the history of tort reform and focusing on changes in physician

supply around adoption of reform, we find the data are not consistent with the usual

theory for why supply might drive punitive damage caps. The usual theory is that

states adopt liability-reducing reforms in order to stem a decline in physician supply.

Figure 5 illustrates this argument in the context of total damage caps, a reform that

is always targeted at physicians. Supply was falling before adoption of total damages

caps; after adoption supply recovered. By contrast, Figure 1 shows that supply was

rising before adoption of punitive damages caps, a reform that reduced liability.

A related concern is that adoption of punitive damage caps might be correlated

with unobserved variables that affect physician supply. For example, business-friendly

states may attract physicians because they make it easy to set up a new practice, and

coincidentally these states may also be more likely to pass tort reform. If this were

the case, we would expect to observe a trend in physician supply both before and

after the enactment of punitive damage caps. But, Figure 1 shows a pre-trend only.

Finally, Figure 6 provides evidence consistent with the plausible exogeneity of

punitive damages caps by showing that per capita income and medical transfer pay-

ments, variables that may be important to physician labor supply, do not appear to

be correlated with the passage of reform.

While these arguments suggest that pre-trends may not be due to endogeneity,

they do not directly address anticipation. To justify estimation of anticipation effects,

one must show that physicians could directly or indirectly anticipate the reform years

prior to adoption.

Physicians clearly have a large incentive to care about tort reform because it affects

their insurance premiums.14 For example, neurosurgeons in St. Clair County, Illinois,

paid an average premium of $228,396 in 2004, but their colleagues in neighboring

Wisconsin, which is not as friendly to plaintiffs, paid less than one-fifth of that (The

Economist 2005). Correctly anticipating future reforms is important for at least

14Even if doctors can pass these costs through to patients, many uninsurable risks such as repu-tational effects and lost time remain. See Currie and MacLeod (2008) for additional discussion.

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Figure 5: Excess physician supply before and after total damage caps: annual leads andlags from 5 years before to 5 years after adoption

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�� �� �� � � � �

��������������� ���������������������

������������������������

This figure plots the normalized coefficients λj from the following regression: yist = Σ5j=−5

λjDst+j +γis+γst+uist,

where yist is the log of the physician count for specialty i in state s in year t, Dst+j is an indicator for whether

total damage caps was first adopted in period t+ j, and γis and γst represent state-specialty and specialty-year fixed

effects.

three reasons. First, relocation costs are large so it is advantageous to locate in a

state where tort liability laws are not only currently physician-friendly but also are

expected to remain that way. Chou and Lo Sasso (2009) present evidence from a

survey of graduating medical residents that tort laws significantly affect a physician’s

practice location choice.15 Second, some changes to tort reforms are implemented

retroactively (Avraham 2007). Third, assets accumulated prior to adoption of reforms

are at risk (or removed from risk) after reforms. Therefore, the economic return to

current supply depends on future liability rules.

Newspaper articles are one obvious channel through which physicians could be

alerted to forthcoming reform. We investigated this possibility by searching the news-

paper archives of Pennsylvania, the largest state that adopted punitive damage caps

15The change in physician supply resulting from tort reform is most likely due to the large inflow ofnew residents and outflow of retirees because it is costly for currently practicing physicians to movestates (Kessler, Sage, and Becker 2005). We are unfortunately unable to verify this with our data.However, we did perform a simple calculation using the published fact that in 1996 approximatelyfive percent of the physicians in our sample were new residents (AMA 1997). Extrapolating thistrend implies that more than one half of all practicing physicians entered the profession within thepast 14 years.

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Figure 6: Per capita income and medical transfer payments are uncorrelated withenactment of punitive damage caps

(a) Per capita income

!1500

!1000

!500

0

500

1000

1500

!6 !4 !2 0 2 4 6

Excess!per!capita!income!($)!

Year!relative!to!adoption

Point"estimate 95%"Confidence"interval

(b) Per capita medical transfers

!0.15

!0.1

!0.05

0

0.05

0.1

!6 !4 !2 0 2 4 6

Excess!per!capita!M

edicare!payments!(thousands!$)

Year!relative!to!adoption

Point"estimate 95%"Confidence"interval

Source: REIS and Avraham (2010). This figure plots the normalized coefficients λj from the following regression:

yst = Σ5j=−5

λjDst+j + γs + γt + ust, where yst is per capita income or medical transfers in state s in year t, Dst+j

is an indicator for whether punitive damage caps is adopted in period t + j, and γs and γt are state and year fixed

effects.

and that also has an online database of newspaper articles available prior to adoption.

Pennsylvania adopted punitive damage caps on January 25, 1997, and, conveniently,

adopted no other reforms during that decade. We found eighty-four articles published

in its two largest local newspapers mentioning “tort reform” prior to 1997. Figure

7 displays the frequency of these articles in each quarter preceding the reform and

shows the policy discussion took place over an extended period of time. One article

published about two years prior to enactment wrote that “the key goals of the [state]

administration...have been to place a cap on punitive-damage awards”(Siegel 1995).

Finally, we briefly discuss why physician supply should respond at all to punitive

damages. It has been reported that punitive damages are awarded in only 1-4% of

all medical malpractice trials (Cohen 2004, Cohen and Harbacek 2011). However,

this figure underestimates the impact of punitive damages. First, according to Table

3, nineteen states have adopted caps on punitive damages. Since the 1-4% figure is

a national figure, it reflects both states that allow punitive awards and states that

cap or prohibit those awards. Punitive damages will play a larger role in states that

do not cap those damages. Second, even if punitive damages are a small percentage

of awards, they may be the one aspect of tort damages that cannot be insured by

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Figure 7: Frequency of articles mentioning tort reform in Pennsylvania, by quarter

0

5

10

15

20

25

1993Q1 1993Q3 1994Q1 1994Q3 1995Q1 1995Q3 1996Q1 1996Q3 1997Q1

Newspaper!articles

Quarter

Adoption!of!punitive

damage!caps!reform

Pennsylvania adopted punitive damage caps reform on January 25, 1997. This figure shows the distribution over time

of the 84 articles in The Philadelphia Inquirer and The Pittsburgh Post-Gazette mentioning the term “tort reform”

during the four years prior to reform. Online archives are unavailable prior to 1993.

physicians. Nearly half the states do not allow malpractice liability insurance to

cover punitive damages (McCullough, Campbell, and Lane LLP 2004; Wilson et al.

2008).16 Moreover, even in states that allow liability insurance to cover punitive

damages, many insurers refuse to do so. It is not surprising, therefore, that a number

of papers that examine medical malpractice tort reform have found a significant effect

of punitive damages on physician behavior (Avraham 2007, Avraham, Dafny, and

Schanzenbach 2010, and Currie and MacLeod 2008).

4.4 Empirical strategy

We estimate the effect of caps on punitive damages on the log of physician supply us-

ing a difference-in-differences strategy. Treatment effects are identified by comparing

within-state changes in physician supply among states that adopt reform to within-

16Viscusi and Born (2005) estimate that medical malpractice insurers incur 6-7% lower losses instates that prohibit insurance coverage of punitive awards. Given that 98.8% of total malpracticeawards are covered by liability insurance (Zeiler et al. 2007), this implies that punitive damagesare a disproportionate source of risk to doctors, perhaps more than 83% (= 6%/(6%+ 1.2%)) of allfinancial risk they bear from medical malpractice liability.

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Figure 8: Cumulative number of states implementing punitive damage caps

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state changes in supply among states that do not adopt reform. It would be sufficient

to include state and year fixed effects to implement our difference-in-differences es-

timator. However, we go further and employ state-specialty and specialty-year fixed

effects. The former control for specialty-level unobservables within each state. The

latter allow time paths for physician supply to vary across specialty, as Figure 4

suggests may be appropriate.

We must select a pre- and a post-treatment period in order to implement our

difference-in-differences design. We could use the entire 1980-2001 panel to calculate

these contrasts but this is unappealing: observations from states that adopted reform

early (late) would receive less weight in the pre (post) period than states that adopted

reform later (earlier). Figure 8 shows that all reforms adopted during our sample

period occurred between 1984 and 1998 (the circled points). Given the 1980 beginning

and 2001 end of our sample, we implement the widest window that permits full pre

and post coverage for each treated state: a 9-year pre-post moving window that

includes the 5 years preceding adoption of punitive damage caps and the 4 years

following adoption.17

Our main identifying assumption is that the adoption of punitive damage caps

17Appendix D presents results for alternative windows. Including all available years generatessimilar results. Including less than four years in the pre- and post-periods causes estimates from thequasi-myopic model to become insignificant. Including less than three years causes all estimates tobecome insignificant due to lack of statistical power.

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is exogenous. We estimate several different specifications in order to increase the

plausibility of this assumption. First, punitive damage caps are most likely to be ex-

ogenous in states where the reform is not targeted solely at medical malpractice cases

(see Table 3). We therefore estimate specifications with and without these potentially

endogenous states.18 Second, even if punitive damage caps are exogenous, other tort

reforms may not be, and their endogeneity could contaminate our estimates. We

thus also estimate specifications that exclude these other tort reforms as controls,

though this may introduce omitted variable bias if tort reforms are correlated. Third,

although we have argued that punitive damage caps were adopted for reasons un-

related to physician supply, skeptics may still worry that states endogenously adopt

reform in response to trends in physician supply. We rule out this possibility by also

estimating specifications that include state trends.

We begin by estimating a baseline myopic model:

yist = βmyopic0 dst + γis + γit + γs × t+ uist (9)

The outcome yist is the log of the number of physicians per capita practicing specialty

i in state s in period t, dst is an indicator for the presence of punitive damage caps in

state s in period t, and γis and γit are state-specialty and specialty-year fixed effects,

respectively. Some specifications that we estimate also include state trends, γs × t.

The ex post effect of reform is estimated by β̂myopic0 . Because this model ignores

anticipation, it implicitly assumes the ex ante effect of reform is equal to zero.

Next, we turn to models that account for anticipation. The quasi-myopic model

addresses anticipation by including leading indicators for whether reform is adopted:

yist = βquasi0 dst + ΣS

j=1βquasij Ds,t+j + γis + γit + γs × t+ uist (10)

We estimate four versions of (10) so that we can allow the number of leading indica-

tors, S, to range from one to four. Ds,t+j is a dummy variable equal to 1 if a reform

is adopted in time period t+ j. For example, if a reform is adopted in period 5, then

Ds,t+1 = 1 in period 4 and 0 otherwise. The coefficient β̂quasi0 identifies the ex post

effect of treatment. The ex ante effect in period t− j is estimated by β̂quasij .

The quasi-myopic model replaces expectations of reform, Et[Ds,t+j], with realiza-

tions of reform, Ds,t+j, and thus implicitly assumes perfect foresight. It also assumes

18The potentially endogenous states are CO, IL, OR, PA, VA, and WI.

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that expectations over a time horizon greater than length S do not matter. Estima-

tion is inconsistent if either of these assumptions fails to hold.

An alternative solution is to assume that individuals discount the future exponen-

tially and have rational expectations. This imposes no restrictions on the length of

the time horizon for expectations and relaxes the assumption of perfect foresight:

yist = θyis,t+1 + βdst + δds,t+1 + γis + γit + γs × t+ wist (11)

The regressor ds,t+1 accounts for the binary nature of treatment, as described in

Appendix C. The forecast errors contained in the error term, wist, cause the lead

dependent variable, yis,t+1, to be endogenous. We estimate equation (11) first using

OLS, then using leads of the outcome variable (yt+j, j ≥ 2) as instruments for yis,t+1,

and finally using lags of the outcome variable (yt−j, j ≥ 2) as instruments. The key

identifying assumption is that the lags and leads of physician supply are uncorrelated

with unobserved determinants of current supply. This imposes a restriction on the

degree of serial correlation in the error term. Arellano and Bond (1991) derive a test

commonly used to check this assumption. We report those tests in our tables.

In the exponential discounting model, the ex post effect is equal to β̂/(1− θ̂) and

the ex ante effect in period t− j is equal to β̂Σ∞

i=j θ̂i. Note that one can evaluate the

statistical significance of the ex ante effect by testing the nonlinear null hypothesis

βθ = 0.19 We report those test results in our tables.

A weak instrument test for panel GMM does not exist.20 This is problematic

because employing a large number of weak instruments can bias estimation. As

a robustness check, we estimate additional IV specifications that employ only one

instrument. This is less efficient than employing all available instruments, but also

less prone to bias.

We weight all estimations by state population because yist is a per capita measure.

Standard errors are clustered at the state level. We employ one-step GMM estimation

when estimating the exponential discounting model to alleviate concerns about finite

19Similarly, the statistical significance of the ex post effect can be evaluated by testing the nullhypothesis β = 0. It is well known that Wald tests of nonlinear restrictions are not invariantto algebraically equivalent restrictions. Existing evidence suggests researchers should use simplemultiplicative forms when possible (Phillips and Park 1988).

20Clemens and Bazzi (2009) suggest that researchers estimate a two-stage least squares model inthese cases to ensure that their instruments are not radically weak. When we do this for (11) weobtain first-stage partial F statistics substantially larger than 10.

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sample problems associated with two-step GMM estimation (Doran and Schmidt

2006; Judson and Owen 1999). Since we do not have data on physician counts for

1984 or 1990, we transform our data using forward orthogonal deviations instead of

the usual first differences when estimating the exponential discounting models because

this preserves sample size in panels with gaps (Arellano and Bover 1995; Roodman

2009).21

4.5 Results and discussion

We first report estimates from a myopic model – our baseline model (9) – that ignores

expectations. Column 1 of Table 4 estimates that caps on punitive damages increases

a state’s equilibrium supply of physicians by 4.5% relative to states that did not

adopt the reform. This is the myopic model’s estimate of what we call the ex post

effect. This estimate increases if we exclude potentially endogenous states (Column 2)

and decreases slightly if we instead exclude all other tort reforms from the regression

(Column 3). Columns 4 and 5 show that the estimated effect decreases substantially

if we include state-specific trends. The specification in Column 5 is the most robust

to an endogeneity critique because it excludes endogenous states, omits other reforms

from the regression, and includes state trends. We thus adopt it as our preferred

specification for accounting for anticipation effects. For compactness, we confine

subsequent estimates to the specifications presented in Columns 2 and 5.22

Estimates of the ex post effect from the quasi-myopic model are slightly larger, but

generally yield insignificant estimates of the ex ante effect. We report those results in

Tables 5 and 6, which correspond to the specifications reported in Columns 2 and 5

from Table 4, respectively. The first column in each table replicates the corresponding

baseline estimate from Table 4. Columns 2 - 5 in each table report estimates for

versions of the quasi-myopic model, with each column sequentially adding one lead

to the model. The coefficient estimates on the time-t treatment variable identify

the ex post effect of reform, including anticipation effects, and can be interpreted as

relative changes in physician supply. Moving across the first row of Table 5 shows

21Let yit be a variable. Then the transformed version under forward orthogonal deviations is equalto y∗t+1 = cit(yit −

1

Tit

ΣTit

j=t+1yij), where Tit is the number of available future observations and cit is

a scale factor equal to√

Tit/(Tit + 1).22Estimates for the specification presented in Column 1 are available in Appendix D. Estimates

for the other two specification (Columns 3 and 4) are similar to those presented in the main text.

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that the estimated ex post effect increases monotonically from 7.1% to 8.9% as we

add leads. Table 6, our preferred specification, reveals a similar pattern. It estimates

an ex post treatment effect of 1.5%, which is slightly larger than the corresponding

baseline estimate of 1.1%. As with the myopic model, introduction of state trends

dramatically reduces treatment effects. The estimated ex ante effects in Column 5 of

Table 6 range from 0.002 to 0.005 and are insignificant.

The exponential discounting model (11) yields even higher estimates of the ex

post effect and typically yields significant ex ante effects. Column 1 of Table 7 reports

OLS estimates of the exponential discounting model. Columns 2 and 3 instrument

for yis,t+1 using leads and lags, respectively, of the outcome variable. The estimated

coefficient on the lead dependent variable, θ̂, is significant across all three models.

The estimated coefficient on the treatment variable, β̂, is significant in the first two

columns of Table 7 but insignificant in Column 3, when we instrument for yis,t+1

using lags. The estimated ex post effect of treatment ranges from 6.1% to 7.7% is

statistically significant except when we instrument using lags. Table 8, our preferred

specification, reveals broadly similar results. It shows an estimated ex post effect of

1.8% when using leads as instruments. The estimated effect is again insignificant,

however, when we instrument with lags. Finally, Table 8 reports ex ante effects that

range from 0.1% to 1.8% when leads are used as instruments. The Wald test of

the hypothesis that β̂θ̂ = 0 shows these effects are statistically significant. When

we employ lags as instruments, however, our point estimates fall close to zero and

become insignificant.

To address the concern that the instruments we employ are overfitting the model,

we re-estimate the exponential discounting model (11) but use only one lead of the

outcome variable as the instrument. We report those results in Table 9. A compar-

ison with Tables 7 and 8 reveals that employing only one instrument increases the

estimated effect, which suggests that our previous estimates may have been biased

downwards in magnitude. Our preferred specification, presented in Columns 5 and 6

of Table 9, estimates an ex post treatment effect of 2.2-2.6%. This is larger than the

corresponding quasi-myopic estimate of 1.5% and more than double the estimated

effect of 1.1% from the baseline myopic model.

The exponential discounting model assumes that treatment has a constant ex

post effect effect over time and we estimate it assuming that agents have rational

expectations. The first assumption is supported by Figure 1. Although it displays

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a small visible decline after adoption of treatment, statistical tests (not reported)

indicate the decline is not significant.

Assessing the plausibility of the rational expectations assumption is more difficult,

though our estimates do not cast doubt on it. A barometer of whether a rational

expectations assumption is reasonable is the size of the estimated discount rate, θ̂. In

many standard economic models, the discount rate is equal to 1/(1 + r), where r is

the interest rate. Although it is difficult to estimate precisely, an estimate of θ̂ near 0

(implying an enormous interest rate) or greater than 1 (implying a negative interest

rates) indicates model misspecification, perhaps because agents do not have rational

expectations. Column 6 from Table 9 estimates θ̂ = 0.735, implying an interest rate

of 36 percent. This is in the upper range of estimates from the literature (Warner

and Pleeter 2001).

We explained in Section 2.1 that the estimated treatment effect in a myopic model

often will typically underestimate the true ex post effect of reform. Including leads

can mitigate this problem by reducing omitted variable bias. Tables 10 - 6 show that

the estimated effects from a quasi-myopic model are larger than the corresponding

estimates from the myopic model, as predicted. The fact that these estimates increase

as we keep adding leads to the quasi-myopic model suggests that each additional

lead moves us closer to an unbiased estimate of the ex post effect. The exponential

discounting model yields even larger estimates, suggesting that anticipation effects

may matter for longer than the data permit in the quasi-myopic model.

That said, the differences between the estimated ex post effects for any two par-

ticular specifications is not statistically significant due to the large standard errors.

Furthermore, the similarity of the point estimates from the quasi-myopic model and

the exponential discounting model suggests that the choice between these two pa-

rameterizations of expectations is not critical to estimates of anticipation effects from

punitive damages caps. However, some of the quasi-myopic models, and nearly all

the exponential discounting models, estimate a statistically significant ex ante effect.

This differs from the myopic model, which implicitly assumes it is equal to zero.

Like other prior studies on this topic, we do not account for general equilibrium

effects. A physician fleeing one state necessarily enters another, magnifying the rela-

tive supply differences between the two states. Kessler, Sage, and Becker (2005) have

previously demonstrated, however, that most of the equilibrium adjustment comes

from newly graduated residents deciding where to practice and retirees leaving prac-

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tice. Furthermore, we are primarily interested in the relative differences between

our model estimates, for it is these relative differences that reveal the importance of

anticipation effects.

Our results are consistent with Currie and MacLeod (2008), who find that joint

and several liability and punitive damage caps have a significant effect on birth out-

comes. Our estimated effects, which range from about 2 to 6%, are similar in mag-

nitude to other studies of tort reform and physician supply. For example, Kessler,

Sage, and Becker (2005) estimate an effect of 3% for a broad set of reforms, Klick and

Stratmann (2007) estimate an effect of 6% for noneconomic damage caps, and Matsa

(2007) estimates an effect of 10% for total damage caps.

5 Conclusion

Researchers are confronted with forward-looking agents in a variety of different appli-

cations, including durable goods purchases, rational addiction, and human and physi-

cal capital investments. In all these cases, anticipation causes outcomes to respond to

future treatment. Incorrectly assuming that this change is due to endogeneity rather

than anticipation will produce biased estimation. While not all economic decisions

are made with an eye towards the future and not all shocks are anticipated, enough

are that empirical work should consider how to define and estimate treatment effects

in the context of anticipation effects.

The framework we introduce in this paper for comparing and estimating different

models of anticipation effects has a number of limitations. Foremost, we offer no clean

test that distinguishes between anticipation and endogeneity. Our application merely

provides informal evidence in favor of anticipation and thus our framework. Further,

within our framework, we offer no formal way to discriminate between the different

sets of parametric restrictions we discuss. There may be other restrictions a researcher

might employ or estimation strategies that do not require any restrictions at all. For

example, if two agents are both treated but one found out about the treatment

earlier than the other, one could estimate anticipation effects with a difference-in-

differences estimator that would eliminate many expectations terms. Likewise, there

may be alternative models of updating or belief formation that can be employed.

Ideally the researcher would directly survey agents about their expectations or at least

survey a subsample to empirically estimate the relationship between expectations and

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observables. Each of these limitations is a useful topic for future research.

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TablesTable 1: Physician specialties by risk tier

Tier 1 Tier 2 Tier 3 Tier 4

Emergency medicine Anesthesiology Allergy & immunol-ogy

Diabetes

General practice General surgery Dermatology Medical oncologyNeurological surgery Orthopedic surgery Nephrology Neoplastic diseasesObstetrics & gynecol-ogy

Plastic surgery Physical medicine &rehabilitation

Psychiatry

Thoracic surgery Radiology Rheumatology Public health &general preventivemedicine

Source: Klick and Stratmann (2007). Specialties in tier 1 exhibit the highest average medical malpractice award per

doctor and specialties in tier 4 exhibit the lowest average.

Table 2: Tort reform descriptions

Tort reform Description

Collateral source Allows damages to be reduced by the valueof compensatory payments already made tothe plaintiff

Contingency fees Places limits on attorney contingency feesJoint and several Limits damages recoverable from parties

only partially responsible for the plaintiff’sharm

Noneconomic damage caps Limits awards for noneconomic damages inmalpractice cases

Periodic payment Requires part or all of damages to be paidin the form of an annuity

Punitive damage caps Prohibits or limits recovery of punitivedamages from physicians

Punitive evidence Requires plaintiff to show by clear and con-vincing evidence that a defendant actedrecklessly

Split recovery Requires some of the punitive damages togo to a state fund for uncompensated tortvictims

Total damage caps Limits awards for total damagesVictims’ fund Establishes a no-fault compensation fund

for medical malpractice victims

Source: Avraham (2010).

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Table 3: Summary of tort reform laws enacted during 1980-2001

Tort reform States enacting tort reform Proportion medical

Collateral source AL (87), CO (87), CT (85), HI(87), ID (90), IN (87), KY (89), MA(87), ME (90), MI (86), MN (85),MT (88), ND (88), NJ (88), NY(85), OR (88), UT (87), WI (95)

0.44

Contingency fees CT (87), FL (86), HI (87), IL (85),MA (87), ME (89), MI (85), NH(87), UT (86)

0.44

Joint and several AK (86), AZ (87), CA (86), CO (87),CT (87), FL (86), GA (88), HI (87),IA (84), ID (88), LA (81), MI (87),MN (89), MO (86), MS (90), MT(88), ND (88), NE (92), NH (90), NJ(88), NM (82), NY (87), TN (92),TX (86), UT (86), WA (86), WI (94),WV (86), WY (86)

0.14

Noneconomic damage caps AK (86), AL (87), CO (87), FL(89), HI (87), ID (87), IL (95), KS(87), MA (87), MD (87), MI (87),MN (86), MO (86), MT (96), ND(96), OR (88), UT (88), WA (86),WI (86), WV (86)

0.55

Periodic payment AZ (89), CO (89), CT (88), FL(87), IA (88), ID (88), IL (86), IN(85), LA (85), MD (87), ME (87),MI (86), MN (89), MO (86), MT(87), NY (86), OH (88), RI (88),SD (88), UT (86), WA (86)

0.62

Punitive damage caps AK (98), AL (87), CO (87), FL (87),GA (88), IL (85), IN (95), KS (88),NC (96), ND (93), NH (87), NJ (96),NV (89), OK (96), OR (88), PA(97), TX (88), VA (89), WI (85)

0.26

Punitive evidence AK (86), AL (87), AZ (87), CA (88),DC (96), FL (00), GA (88), IA (87),ID (88), IN (84), KS (88), KY (89),MD (92), ME (85), MO (86), MS(94), MT (85), NC (96), ND (87), NJ(96), NV (89), OH (88), OK (87), OR(88), SC (88), TN (92), TX (88), UT(90), WI (95)

0.03

Split recovery AK (98), CO (87), FL (87), IA (87),IN (96), OR (88), UT (90)

0.14

Total damage caps CO (89), SD (86) 1Victims’ fund ND (83) 1

Source: Avraham (2010). Year of enactment given in parentheses. Bold face indicates the reformapplies to medical malpractice torts only. The third column presents the proportion of all adoptedreforms that applied to medical malpractice torts only.

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Table 4: OLS estimates of baseline myopic model

(1) (2) (3) (4) (5)

Ex post effect (β̂myopic0

) 0.045** 0.071* 0.034* 0.006 0.011*(0.022) (0.035) (0.020) (0.008) (0.006)

Exclude IL, OR, PA, VA, WI No Yes No No YesExclude tort controls No No Yes No YesState trends No No No Yes YesObservations 6,493 6,103 6,493 6,493 6,103R-squared 0.990 0.990 0.990 0.993 0.992

This table reports estimates of equation (9). Dependent variable is log of count of high-risk physicians per 100,000population. All estimates include state-specialty and specialty-year fixed effects. Standard errors, given in parentheses,are clustered by state. A */** next to the coefficient indicates significance at the 10/5% level.

Table 5: OLS estimates of myopic and quasi-myopic (QM) models: exclude endogenousstates, all controls, no trends

(1) (2) (3) (4) (5)

Ex post effect (β̂quasi0

) 0.071* 0.074* 0.080* 0.083** 0.089**(0.035) (0.037) (0.040) (0.041) (0.044)

Ex ante effect (t-1) (β̂quasi1

) 0.016 0.022 0.026 0.031(0.014) (0.019) (0.021) (0.024)

Ex ante effect (t-2) (β̂quasi2

) 0.019 0.023 0.028(0.015) (0.017) (0.021)

Ex ante effect (t-3) (β̂quasi3

) 0.011 0.016(0.009) (0.013)

Ex ante effect (t-4) (β̂quasi4

) 0.015(0.015)

Model Myopic QM QM QM QMExclude IL, PA, OR, VA, WI Yes Yes Yes Yes YesExclude tort controls No No No No NoState trends No No No No NoObservations 6,103 6,103 6,103 6,103 6,103R-squared 0.990 0.990 0.990 0.990 0.990

This table reports estimates of equation (10). Dependent variable is log of count of high-risk physicians per 100,000population. All estimates include state-specialty and specialty-year fixed effects. Standard errors, given in parentheses,are clustered by state. A */** next to the coefficient indicates significance at the 10/5% level.

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Table 6: OLS estimates of myopic and quasi-myopic (QM) models: exclude endogenousstates, no controls, trends

(1) (2) (3) (4) (5)

Ex post effect (β̂quasi0

) 0.011* 0.013* 0.012 0.014 0.015*(0.006) (0.007) (0.009) (0.009) (0.009)

Ex ante effect (t-1) (β̂quasi1

) 0.002 0.002 0.003 0.004(0.005) (0.007) (0.007) (0.006)

Ex ante effect (t-2) (β̂quasi2

) -0.000 0.001 0.002(0.007) (0.007) (0.007)

Ex ante effect (t-3) (β̂quasi3

) 0.004 0.005(0.004) (0.005)

Ex ante effect (t-4) (β̂quasi4

) 0.002(0.004)

Model Myopic QM QM QM QMExclude IL, PA, OR, VA, WI Yes Yes Yes Yes YesExclude tort controls Yes Yes Yes Yes YesState trends Yes Yes Yes Yes YesObservations 6,103 6,103 6,103 6,103 6,103R-squared 0.992 0.992 0.992 0.992 0.992

This table reports estimates of equation (10). Dependent variable is log of count of high-risk physicians per 100,000population. All estimates include state-specialty and specialty-year fixed effects. Standard errors, given in parentheses,are clustered by state. A */** next to the coefficient indicates significance at the 10/5% level.

Table 7: OLS and IV estimates of exponential discounting model: exclude endogenousstates, all controls, no trends

(1) (2) (3)

Discount rate (θ̂) 0.693** 0.543** 0.696**(0.052) (0.121) (0.073)

Punitive damage caps (β̂) 0.019* 0.035** 0.023(0.010) (0.015) (0.015)

Calculated effects

Ex post effect (β̂/(1− θ̂)) 0.061 0.077 0.075

Ex ante effect (t-1) (β̂Σ∞

i=1θ̂i) 0.042 0.042 0.052

Ex ante effect (t-2) (β̂Σ∞

i=2θ̂i) 0.029 0.023 0.036

Ex ante effect (t-3) (β̂Σ∞

i=3θ̂i) 0.020 0.012 0.025

Ex ante effect (t-4) (β̂Σ∞

i=4θ̂i) 0.014 0.007 0.018

Wald test: β̂θ̂ = 0 (p-value) 0.087 0.032 0.123

IV None Leads LagsExclude IL, PA, OR, VA, WI Yes Yes YesExclude tort controls No No NoState trends No No NoObservations 5,139 4,218 4,859AR(3) test (p-value) N/A 0.897 0.956

This table reports OLS and IV estimates of equation (11). Dependent variable is log of count of high-risk physiciansper 100,000 population. All estimates include state-specialty and specialty-year fixed effects. Standard errors, givenin parentheses, are clustered by state. A */** next to the estimated coefficient β̂ or θ̂ indicates significance at the10/5% level. Null hypothesis of the AR(3) test is that the estimated residuals are not third-order autocorrelated.

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Table 8: OLS and IV estimates of exponential discounting model: exclude endogenousstates, no controls, trends

(1) (2) (3)

Discount rate (θ̂) 0.598** 0.495** 0.489**(0.044) (0.117) (0.080)

Punitive damage caps (β̂) -0.001 0.009** 0.001(0.007) (0.004) (0.005)

Calculated effects

Ex post effect (β̂/(1− θ̂)) -0.002 0.018 0.003

Ex ante effect (t-1) (β̂Σ∞

i=1θ̂i) -0.001 0.009 0.001

Ex ante effect (t-2) (β̂Σ∞

i=2θ̂i) -0.001 0.004 0.001

Ex ante effect (t-3) (β̂Σ∞

i=3θ̂i) -0.000 0.002 0.000

Ex ante effect (t-4) (β̂Σ∞

i=4θ̂i) -0.000 0.001 0.000

Wald test: β̂θ̂ = 0 (p-value) 0.925 0.012 0.789

IV None Leads LagsExclude IL, PA, OR, VA, WI Yes Yes YesExclude tort controls Yes Yes YesState trends Yes Yes YesObservations 5,139 4,218 4,859AR(3) test (p-value) N/A 0.868 0.913

This table reports OLS and IV estimates of equation (11). Dependent variable is log of count of high-risk physiciansper 100,000 population. All estimates include state-specialty and specialty-year fixed effects. Standard errors, givenin parentheses, are clustered by state. A */** next to the estimated coefficient β̂ or θ̂ indicates significance at the10/5% level. Null hypothesis of the AR(3) test is that the estimated residuals are not third-order autocorrelated.

Table 9: Estimates of exponential discounting model when employing only one IV

(1) (2) (3) (4) (5) (6)

Discount rate (θ̂) 0.593** 0.719** 0.563** 0.673** 0.639** 0.735**(0.144) (0.176) (0.172) (0.229) (0.133) (0.151)

Punitive damage caps (β̂) 0.032** 0.027** 0.034** 0.026 0.008** 0.007**(0.012) (0.012) (0.015) (0.018) (0.003) (0.003)

Calculated effects

Ex post effect (β̂/(1− θ̂)) 0.078 0.095 0.077 0.079 0.022 0.026

Ex ante effect (t-1) (β̂Σ∞

i=1θ̂i) 0.046 0.068 0.043 0.053 0.014 0.019

Ex ante effect (t-2) (β̂Σ∞

i=2θ̂i) 0.027 0.049 0.024 0.036 0.009 0.014

Ex ante effect (t-3) (β̂Σ∞

i=3θ̂i) 0.016 0.035 0.014 0.024 0.006 0.010

Ex ante effect (t-4) (β̂Σ∞

i=4θ̂i) 0.010 0.025 0.008 0.016 0.004 0.008

Wald test: β̂θ̂ = 0 (p-value) 0.019 0.014 0.028 0.052 0.004 0.011

IV yt+2 yt+3 yt+2 yt+3 yt+2 yt+3

Exclude IL, PA, OR, VA, WI No No Yes Yes Yes YesExclude tort controls No No No No Yes YesState trends No No No No Yes YesObservations 4,488 4,488 4,218 4,218 4,218 4,218AR(3) test (p-value) 0.899 0.923 0.904 0.926 0.916 0.931

This table reports IV estimates of equation (11). Dependent variable is log of count of high-risk physicians per100,000 population. All estimates include state-specialty and specialty-year fixed effects. Standard errors, given inparentheses, are clustered by state. A */** next to the estimated coefficient β̂ or θ̂ indicates significance at the 10/5%level. Null hypothesis of the AR(3) test is that the estimated residuals are not third-order autocorrelated.

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Appendix

A Adaptive expectations

In this section we derive a model under the assumption that agents have adaptive

expectations and show how to estimate it. One can show that the object of the

agent’s expectations (outcomes or treatment) does not affect identification of β or θ.

For ease of exposition we assume agents have adaptive expectations about outcomes:

Et [yt+1] = Et [yt+j] = φyt + (1− φ)Et−1 [yt]

Plugging these equations into the estimation equation

yt = θEt [yt+1] + βdt + et (12)

and simplifying yields

yt = θφyt + θ (1− φ)Et−1 [yt] + βdt + εt (13)

The one-step back version of equation (12) is:

yt−1 = θEt−1 [yt] + βdt−1 + εt−1

Solve this for Et−1 [yt] and plug the result into (13). Simplifying then produces the

estimable equation

yt = γ (1− φ) yt−1 + γβdt − γβ (1− φ) dt−1 + γεt − γ (1− φ) εt−1

where γ ≡ 1/ (1− θφ). Time-t outcomes are now a function of past rather than future

outcomes. The reason is that adaptive expectations is a backward-looking model of

learning. The coefficient on current treatment no longer directly identifies β, though

that parameter can be identified. Finally, the only source of endogeneity is previous

period model error: E [yt−1εt−1] 6= 0. Estimation is therefore straight-forward (so

long as there is no serial correlation in εt): use lags of order three or deeper and/or

leads of order one or higher as instruments.

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B Rational expectations about outcomes

Consider the case where the agent is able to form rational expectations about out-

comes.23 Initially we assume realizations are a function of expectations: yt+j =

Et [yt+j] + vyt,t+j, where vyt,t+j indicates the error given time t expectations about out-

comes in time t+j and E[Et [yt+j] vyt,t+j] = 0. This model is appropriate, for example,

when outcomes are stock prices since realizations of stock prices are a composite of

expectations (e.g., Chow 1989). Expectations at time t about θyt+1 are

θEt [yt+1] = Et

[θβΣ∞

j=0θjEt+1 [dt+1+i]

](14)

since Et [et+1] = 0. Subtracting (14) from (4) yields

yt = θEt [yt+1] + βdt + et (15)

Plugging in our rational expectations assumption produces the estimation equation

yt = θyt+1 + βdt + wt (16)

where wt = et − θvyt,t+1.

The error term has two components, model error (et) and unexpected, mean-zero

forecast error (vyt,t+1), which cause outcomes to deviate from forecasts. Thus rational

expectations introduces measurement error. The result is endogeneity between next

period’s outcome yt+1 and vyt,t+1. Furthermore, if {dt} are serially correlated, then dt

would be correlated with yt+1 and thus vyt,t+1 through dt+1.

If we had instead assumed expectations about outcomes were a function of actual

outcomes, i.e., Et[yt+j] = yt+j + vyt,t+j where E[yt+jvyt,t+j] = 0, then there would be

no endogeneity. The Euler equation would look the same, but wt = et + θvyt,t+1. By

assumption yt+1 is exogenous, and even with serial correlation in {dt} we would have

E[dtvyt,t+1] 6= 0.

Estimating this model is straightforward. Suppose that expectations are a function

23We ignore the role of covariates xt to simplify the exposition. However, it is straightforward toincorporate covariates into the analysis.

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of outcomes and Et [yt+1] = yt+1 + vyt+1.24 Our error term is

wt = et + θvyt+1

The analogue to Assumption A2′ is that, for some constant H,

E [wtwt+j] = E[(et − θvyt+1

)(et+j − θvyt+j+1)] = 0 ∀ j > H

If et and vyt are serially and mutually uncorrelated then the usual difference and system

GMM estimators can be used so long as Assumptions A1 and A3 hold. Limited

correlation in the error term can be accommodated by using higher order leads.

C Binary treatment variables

In many applications the treatment variable, dt, is binary. The forecast error corre-

sponding to rational expectations of a binary variable is necessarily mean reverting,

which induces a negative correlation between dt+j and vdt,t+j.25 If treatment states

are correlated over time then endogeneity occurs because E[dtvdt,t+j] 6= 0 and the er-

ror term will be serially correlated, violating Assumption A2′ from Section 3.1. This

problem can be resolved if agent forecasts follow a Markov process because then future

treatment states can be used to absorb the endogeneity. More specifically, suppose

that

Cov[dt, vdt,t+j|dt+1] = 0∀t, ∀j > 1

For rational expectations, this assumption can be tested by regressing dt on lags of

dt and showing that, conditional on dt−1, deeper lags are not correlated with dt. If

the assumption holds, one can then consistently estimate the equation

yt = θyt+1 + βdt + δdt+1 + wt

where dt is binary and δ is a nuisance parameter. For interested readers, Monte

Carlo simulations demonstrating the consistency of this estimator are available upon

request.

24If outcomes are a function of expectations (yt+1 = Et [yt+1] + vyt+1), then yt+1 is exogenous andno instruments are required.

25Recall that vdt,t+j is defined as the forecast error from the time-t forecast of dt+j

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We verified that adoption of tort reform follows a Markov process by estimating the

following state-level regression for each tort reform listed in Table 2: dst = α1xst +

α2dst−1 + α3dst−2 + est, where dst is a reform and xst is a vector of controls that

includes all other tort reforms. Our results (not reported) show that, at a 5% level

of significance, α2 is significant for all ten tort reforms while α3 is insignificant for

nine of them. These regressions clustered standard errors at the state level and were

unweighted.

D Robustness checks

Tables 10 and 11 report results for the quasi-myopic and exponential models when our

specification includes all states, all tort controls, and no state trends. The estimates

are similar to the other tables that focus on the states where reforms are more likely

to be exogenous (Tables 5 and 7).

The model estimated in the main text employed the widest window that permitted

full pre and post coverage for each treated state: a 9-year pre-post moving window

that included the 5 years preceding adoption of punitive damage caps and the 4 years

following adoption. In this section, we show that our results are not substantively

affected if we employ alternative windows.

Table 12 displays estimates from all of our models using five different definitions for

the window. For compactness, we present results only for our preferred specification

(exclude endogenous states, omit other tort reforms from the regression, and include

state trends) and only for the coefficient on the time-t treatment variable. The first

column of Table 12 presents results when we employ all available years for both the

pre and the post period. The second column presents results when we employ four

years of data in both the pre and post periods. Columns (3)-(6) sequentially shorten

the number of years in both the pre and post periods.

Estimates from the quasi-myopic model continue to be larger in magnitude than

the corresponding estimates from the myopic model, regardless of whether the pre-

post window includes all available years (Column 1) or fewer years (Columns 2-6). As

we decrease the number of available years in the window, the standard errors increase,

which eventually causes estimates to become insignificant.

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Table 10: OLS estimates of myopic and quasi-myopic (QM) models: all states, allcontrols, no trends

(1) (2) (3) (4) (5)

Ex post effect (β̂quasi0

) 0.045** 0.048* 0.053* 0.059** 0.063**(0.022) (0.024) (0.026) (0.028) (0.031)

Ex ante effect (t-1) (β̂quasi1

) 0.013 0.019 0.025 0.029(0.012) (0.016) (0.018) (0.021)

Ex ante effect (t-2) (β̂quasi2

) 0.019 0.025* 0.030(0.012) (0.014) (0.018)

Ex ante effect (t-3) (β̂quasi3

) 0.017** 0.022*(0.008) (0.011)

Ex ante effect (t-4) (β̂quasi4

) 0.010(0.010)

Model Myopic QM QM QM QMExclude IL, PA, OR, VA, WI No No No No NoExclude tort controls No No No No NoState trends No No No No NoObservations 6,493 6,493 6,493 6,493 6,493R-squared 0.990 0.990 0.990 0.990 0.990

This table reports estimates of equation (10). Dependent variable is log of count of high-risk physicians per 100,000population. All estimates include state-specialty and specialty-year fixed effects. Standard errors, given in parentheses,are clustered by state. A */** next to the coefficient indicates significance at the 10/5% level.

Table 11: OLS and IV estimates of exponential discounting model: all states, allcontrols, no trends

(1) (2) (3)

Discount rate (θ̂) 0.692** 0.544** 0.706**(0.050) (0.117) (0.070)

Punitive damage caps (β̂) 0.021** 0.034** 0.023*(0.009) (0.012) (0.012)

Calculated effects

Ex post effect (β̂/(1− θ̂)) 0.067 0.074 0.078

Ex ante effect (t-1) (β̂Σ∞

i=1θ̂i) 0.046 0.040 0.055

Ex ante effect (t-2) (β̂Σ∞

i=2θ̂i) 0.032 0.022 0.039

Ex ante effect (t-3) (β̂Σ∞

i=3θ̂i) 0.022 0.012 0.028

Ex ante effect (t-4) (β̂Σ∞

i=4θ̂i) 0.015 0.006 0.019

Wald test: β̂θ̂ = 0 (p-value) 0.036 0.021 0.082

IV None Leads LagsExclude IL, PA, OR, VA, WI No No NoExclude tort controls No No NoState trends No No NoObservations 5,479 4,488 5,189AR(3) test (p-value) N/A 0.883 0.955

This table reports OLS and IV estimates of equation (11). Dependent variable is log of count of high-risk physiciansper 100,000 population. All estimates include state-specialty and specialty-year fixed effects. Standard errors, givenin parentheses, are clustered by state. A */** next to the estimated coefficient β̂ or θ̂ indicates significance at the10/5% level. Null hypothesis of the AR(3) test is that the estimated residuals are not third-order autocorrelated.

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Table 12: Coefficient estimates on the time-t treatment effect for different pre-postwindows

(1) (2) (3) (4) (5) (6)

Myopic (β̂myopic) 0.019** 0.011* 0.011* 0.009 0.008 -0.001(0.008) (0.007) (0.006) (0.006) (0.005) (0.007)

Quasi-myopic (β̂quasi0

) 0.021* 0.012 0.019** 0.011 0.009 0.007(0.011) (0.007) (0.008) (0.012) (0.011) (0.014)

Exponential discounting (IV= leads) (β̂) 0.010** 0.008** 0.008** 0.009** 0.008** -0.022(0.002) (0.003) (0.003) (0.003) (0.004) (0.018)

Exponential discounting (IV= lags) (β̂) 0.009** 0.000 0.001 0.002 -0.005 -0.008(0.003) (0.006) (0.007) (0.008) (0.009) (0.012)

Exponential discounting (IV= yt+2) (β̂) 0.008** 0.006** 0.006** 0.008** 0.007 -0.025(0.002) (0.003) (0.003) (0.002) (0.004) (0.021)

Exponential discounting (IV= yt+3) (β̂) 0.008** 0.006* 0.005 0.006* 0.006 -0.026(0.003) (0.003) (0.004) (0.003) (0.005) (0.022)

Exclude IL, PA, OR, VA, WI Yes Yes Yes Yes Yes YesExclude tort controls Yes Yes Yes Yes Yes YesState trends Yes Yes Yes Yes Yes YesPre-post window All years 4-4 4-3 3-3 3-2 2-2

This table displays estimates for different pre-post windows. Column (1) reports estimates when we employ allavailable years. Columns (2) through (6) limit the pre- and post-treatment periods to varying degrees ranging from2 to 4 years. Standard errors, given in parentheses, are clustered by state. A */** next to the coefficient indicatessignificance at the 10/5% level.

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